So referring again to Callie Burt's post, here, while failing to adhere to my own strictures about being brief. I see two major issues.
First, whether the BG side of the debate is being defensive in taking issue with bringing an end to "heritability studies," or by characterizing the Burt et al stance as "anti-BG". Burt insists that she is not anti-BG, but aside from the one strictly theoretical quote I mentioned in the last post, as far as I know there is no evidence of that in any of these articles. She says it wasn't the point of the articles to get into the positive contributions a genetically informed point of view might make, and OK, but then it isn't such a surprise that people take the articles the wrong way. Really, the same can be said for the BG side. Mightn't it be a good idea to pay a little closer attention to the EEA and its consequences, not to mention a million other assumptions that twin studies make? rGE, random mating, the list goes on and on. I think if you go back to classic papers in the seventies and eighties by people like Eaves, Martin, Heath, Loehlin, etc, they worried about these things a lot, all the time. It's just good modeling practice, really.
Both sides of the debate are accusing the other of a scorched earth strategy, and I hope it doesn't make me sound too kum-bye-a to say that finding a way to concede that your opponent might have a point about something is a pretty good way to move forward. Criminology has ignored the possibility of genetic pathways for years; BG sometimes conducts twin studies without putting a hell of a lot of thought into exactly why we are doing it, what the assumptions are, or what the results mean.
Second is the "heritability studies" question. Burt claims that the studies she was criticizing were strictly h2-equals studies. So I read all the studies in the Table. (By the way, what is it with people whose names begin with B in the BG of criminality? Barnes, Beaver, Boutwell, Boisvert. And now Burt! Attn Tim Bates, Tom Bouchard, and Chris Beam). And, drum roll.... the studies in question are not strictly heritability studies, in fact none of them are, although a couple come close. They are bivariate twin studies, so let me say a few words about that.
Let's say a sociologist observes that children who are held back a grade in elementary school are more likely to get arrested in high school. Now of course that is just a correlation, it doesn't mean that getting held back causes delinquency. Randomly assigning kids to getting held back is out of the question. What can be done? So it occurs to the sociologist to find sibling pairs who are discordant for getting held back. Within pairs, it turns out that the one who was held back is no more likely to get arrested than his sibling who was not held back.
What do we conclude from this? Presumably it would decrease our impression that holding-back causes arrest, because if that were true why wouldn't it happen within pairs as well as between them? We might further conclude that the original observed correlation must have been the result of something else that sibling pairs share, eg families and everything that goes along with them. On the other hand, it might turn out that the held-back sibling is more likely to get arrested than the co-sib. Does this prove causation? No, but it strengthens our confidence in a causal hypothesis, as it survived a fairly rigorous test. In the absence of randomization, this may be the best we can do.
My main point is that this sociologist is doing "behavior genetics." Among the familial things that siblings share, of course is half their genes. The other is their family environment. OK, you say, but it isn't a "heritability study". But it is. If you drew sibling pairs at random from the population rather than selecting them for being discordant for held-back, you could partition the held-back variance into a Between and a Within pair component, and B/(B+W) would be the intraclass correlation for sibling pair. The design is not yet genetically informative, so the correlation would be the "familiality" of being held back. If you wanted, you could report this quantity, and include a latent variable for it (like an ACE latent variable) when you analyzed the data.
The key to doing a bivariate twin study clearly, in my view, is recognizing that (a) The variance components (the h2-equal part) are not the main point, (b) The within-pair effects (the genetically informed quasi-experimental regression part) are the main point, and (c) The correct way to analyze the within pair effects is to ensure that they are invariant against changes in the variance components, that is ensuring that (a) doesn't interfere with (b). This is what the Turkheimer and Harden chapter is about.
DZ twins are just siblings, of course, and if you throw in MZ twins and all the assumptions that Burt et al don't like it turns into a bivariate twin study, but the basic logic doesn't change. Held-back and arrest are related between and within pairs, now in MZ and DZ twins. Zygosity and the twin assumptions, if you are so inclined, allow you to divide the "familiality" thing from the sibling study into A and C, and I think it is often interesting to think about whether the confounds of the purported causal effect appear to be genetic or family environmental. However, it remains absolutely true that the magnitude of these components is not the main point-- the within pair relationship between held-back and arrest is the main point, and the data should ideally be analyzed in a way that keeps this relationship invariant to changes in the decomposition of the predictor.
The bivariate criminology twin studies that I read, in my opinion, don't do a great job of keeping the "heritability" issues separate from the within pair regression issues. I would analyze and report the results differently. Burt et al, in the same way, see the MZ and DZ twins and the reported heritabilities, and conclude that they must be "heritability studies" even though they are, at least potentially, more than that. And the great irony is that in most of them, the within pair relationships between X and Y survive the test of having their common genetic background controlled. So in Boutwell et al, for example, there is a significant within-pair relationship between low self-control and victimization. This means that in pairs of identical twins, the twin with lower self-control is more likely than the co-twin to be a victim, controlling for whatever genes and family background identical twins have in common. This is a victory for environmental-- better to say phenotypic-- causation, but it gets lost in both the original report and the objections, because everyone is hung up on worrying about what might have turned out to be heritable.
Well as usual this has turned into more tooting my own horn than resolving this particular debate. My conclusion is that behavior genetics has an important role to play in criminology, not because criminal behavior has in any important sense turned out to be "genetic" or "biological," but instead because criminology is almost always stuck with inferring causal processes from correlational data, and careful use of twins can help rule out important classes of confounds of those causal hypotheses. This is less attention grabbing than concluding that "criminality lurks in the genes" like they said in that infidelity study, but ultimately much more useful scientifically
Friday, June 5, 2015
Thursday, June 4, 2015
Callie Burt Replies
Here. I have a talk to get ready for and I won't be able to think much about this before tonight. It isn't clear to me, in general, how much arguing I want to do here. In some ways that's the point, but it gets old and/or nasty quickly.
One rule I have sometimes considered is that a reply has to be less than half the length of whatever it is replying to. Exponential decay being the rapid process that it is, after a few back and forths the disputants can yell,
Bullshit!
Bull!
#!
!
at each other and that will be the end of it. I think Callie's post is longer than mine, but I hadn't invented the rule yet.
One rule I have sometimes considered is that a reply has to be less than half the length of whatever it is replying to. Exponential decay being the rapid process that it is, after a few back and forths the disputants can yell,
Bullshit!
Bull!
#!
!
at each other and that will be the end of it. I think Callie's post is longer than mine, but I hadn't invented the rule yet.
Monday, June 1, 2015
The Criminology Debate
As most readers will know, there has recently been an extended debate about the value of "heritability studies" in the journal Criminology. Burt and Simons original paper is here, with a reply from Barnes et al here, a rebuttal from Burt and Simons, here, and a reply here. I was briefly involved in the editorial process, between the original paper and the reply. This is a long complicated argument, the authors have done a good job stating their positions, they don't need me to referee it, and I spend far too much time arguing about theory anyway. So I am not going to work my through all of it point by point.
What I do want to comment on is the use of my name as catch-all reference for the idea that "heritability studies" (see Point 3 below) are flawed. Burt and Simons cited me this way in the original article, and then in a very strong way in the first sentence of their rebuttal. Are Burt and Simons really "echoing the calls" of behavioral geneticists in calling for an "end to heritability studies"? That is what I want to address in this post, although I won't be able to resist some more general comments along the way.
1) One problem in this whole debate, evident in the sentence quoted above, is the purple language used on both sides, something I can be guilty of myself. Calling for an end to a certain kind of study sounds a lot like encouraging scientific censorship, which is the way Barnes et al. took it.
2) If nothing else, the generic citations of Rutter and Turkheimer as a kind of appeal to authority is a lousy way to argue. What did I say, exactly, and why is what I said relevant to the current argument? Many people on the BG side of things could care less what Turkheimer says, because they think I am completely wrong. And if people on the other side of the argument were paying attention, they wouldn't like a lot of what I have had to say either, see below. Science isn't about authority.
3) One ongoing problem I have with a lot of recent anti-BG writing is the whole idea of a "heritability study". Evan Charney is another person who trades in this idea. A heritability study isn't a thing. A heritability is a descriptive statistic, an effect size, not a kind of study. It is kind of like writing a critique of social psychology and railing against "F-ratio studies."
4) What Burt and Simons think they mean by a "heritability study" is a study that has no point other than estimating the heritability of something. My friend Ron Yeo used to refer to these as h-squared-equals studies. On this point they can cite me, and the 2011 paper they cite is a reasonable source. The heritability of criminality doesn't mean that it has somehow turned out to be "biological" and whether the estimated value in some twin study is .3 or .65 makes very little difference and doesn't tend to replicate anyway. In fact, the one and only time I have ever written anything about criminal behavior was in my first (1998) paper on this subject, when I got after Sarnoff Mednick for overinterpreting the heritability of criminality. But see next point.
5) Barnes et al are right: I do twin studies for a living, and it would be mighty hypocritical of me to declare that they are useless in general. As a BG person who has spent a lot of time criticizing the heritability concept, I have made it a discipline to never suggest that my doubts about numerical heritabilities should lead to a general dismissal of genetic effects on behavior or the behavior genetic enterprise generally. The one thing that is for sure about the heritability of behavior is that it isn't zero (or one), and while I doubt that this fact has deep implications for how we think about ourselves as human beings (we already knew that we were biological, genetic beings), it has profound implications for how we conduct ourselves as social scientists. Bottom line, it means that we can never interpret correlations among biologically related people, or within individual people across time, as necessarily environmental in origin. This fact has nothing to do with numerical heritabilities, the EEA, rDZ=.5, the additivity of genes and environment, or any of the other long-standing bones of contention. It is true under the loosest possible interpretation of the meaning of quantitative genetics.
6) I suspect that Burt and Simons think they have this point covered. Early in their first paper, they have a very nice paragraph (bottom of 225) about how they have no intention of dismissing the importance of genes for criminal behavior, or of endorsing radical environmentalism or social determinism. That's a nice sentiment, but I don't think they live up to it. Where in the remainder of their articles is a concession that genetic pathways rule out certain interpretations of the data, an acknowledgement that criminology has to take genetics into account when it is interpreting its findings? Like every anti-BG paper I have ever read, they spend the rest of their paper finding something to attack in every single genetically oriented paper they can find. Twin study? EEA. Adoption study? Prenatal effects. If all of non-experimental social science were held to this standard it would just go away. The fuzziness of the "heritability study" concept allows them to fade from doubts about heritability coefficients, with reasonable citations to me, to dismissal of behavior genetics or even quantitative genetics in general, which is wishful thinking and for which I offer no support.
7) Basically, I think post-heritability twin studies are useful as quasi-experimental tools to investigate causal hypotheses about observed associations when random assignment is impossible. The best citation to my ideas about how twins can be used to do useful social science is Turkheimer and Harden (2014), in Reis and Judd, Handbook of Research Methods in Social and Personality Psychology. It's a commercial book and I won't post the link here, but if buying it presents a financial hardship let me know.
8) Now the question is whether the studies that Burt and Simons list are h2-equals-studies or more interesting genetically informed social science. I'm not going to take the time to go through them one at a time, but the several I looked at were bivariate "quasi-causal" (as we call them in our lab) studies. Ironically, the ones I looked at were actually quite consistent with phenotypically causal interpretation, ie the effects don't go away when you control for genetics. This is something that genetic researchers often miss: they think they are supposed to be interested in genetic pathways, A effects, but in fact the interesting hypotheses are usually about E effects, associations within identical twin pairs that remain with genetic differences controlled. See Turkheimer and Harden.
9) Moffitt and Beckley wrote a nice reply about epigenetics and I won't go into depth about it. I think that people who think that epigenetic explanations of behavioral differences are important should go ahead and do the research and show it. I doubt very much that a demonstration of meaningful epigenetic effects would meet with any opposition in the behavior genetic community. Epigenetics of behavior is behavior genetics. Epigenetics and classical genetics aren't at odds on a biological level, and there is no reason they should be at odds in social science.
10) Like a lot of recent anti-BG theorists, Burt and Simon are just wrong about GCTA. I have my doubts about some aspects of GCTA, discussed here. But Burt and Simons cherry pick the few studies that have produced zero GCTA-heritabilities, and ignore the many others that look almost exactly like twin studies with somewhat smaller effects. And it makes perfect sense inside the paradigm that the effects would be smaller. Differences between twin heritabilities and GCTA heritabilities are interesting, varied in magnitude, and as far as I know still awaiting thorough theoretical explanation. But the idea that GCTA has shown that twin studies were wrong all along isn't even close. In fact, the conclusion of my GCTA paper captures my overall thoughts on heritability in both directions, as follows, noting especially the first sentence:
So in conclusion: if you want to cite me as a critic of some general version of BG, the citation should be limited to the idea that numerical heritabilities aren't very important per se, and that studies that do nothing other than estimate them are no longer very important. The next sentence should be something about how I do maintain that nonzero heritability is important methodologically, and that there are many scientifically useful things to do with twins other than just estimating heritabilities. Better yet, be very specific about what it is I am supposed to have said when you cite me.
One more self-quote and I'll shut up. At the end of my 1998 paper (Almost 20 years ago! Yikes.) I said,
I will close with two recommendations, one very practical and the other theoretical, for future discussions of nature-nurture. The practical suggestion is that all sides of the issue should stipulate the first law of behavioral genetics and refrain from further discussion of whether or not the heritability of anything is equal to zero. As a reader of behavioral genetics, keep a pencil by your side and lightly excise everything either asserts nonzero heritability or attempts to explain it away: Much space could be saved in our journals (even those containing sophisticated multivariate genetics or well-informed opposition) if this recommendation were put into effect.
What I do want to comment on is the use of my name as catch-all reference for the idea that "heritability studies" (see Point 3 below) are flawed. Burt and Simons cited me this way in the original article, and then in a very strong way in the first sentence of their rebuttal. Are Burt and Simons really "echoing the calls" of behavioral geneticists in calling for an "end to heritability studies"? That is what I want to address in this post, although I won't be able to resist some more general comments along the way.
1) One problem in this whole debate, evident in the sentence quoted above, is the purple language used on both sides, something I can be guilty of myself. Calling for an end to a certain kind of study sounds a lot like encouraging scientific censorship, which is the way Barnes et al. took it.
2) If nothing else, the generic citations of Rutter and Turkheimer as a kind of appeal to authority is a lousy way to argue. What did I say, exactly, and why is what I said relevant to the current argument? Many people on the BG side of things could care less what Turkheimer says, because they think I am completely wrong. And if people on the other side of the argument were paying attention, they wouldn't like a lot of what I have had to say either, see below. Science isn't about authority.
3) One ongoing problem I have with a lot of recent anti-BG writing is the whole idea of a "heritability study". Evan Charney is another person who trades in this idea. A heritability study isn't a thing. A heritability is a descriptive statistic, an effect size, not a kind of study. It is kind of like writing a critique of social psychology and railing against "F-ratio studies."
4) What Burt and Simons think they mean by a "heritability study" is a study that has no point other than estimating the heritability of something. My friend Ron Yeo used to refer to these as h-squared-equals studies. On this point they can cite me, and the 2011 paper they cite is a reasonable source. The heritability of criminality doesn't mean that it has somehow turned out to be "biological" and whether the estimated value in some twin study is .3 or .65 makes very little difference and doesn't tend to replicate anyway. In fact, the one and only time I have ever written anything about criminal behavior was in my first (1998) paper on this subject, when I got after Sarnoff Mednick for overinterpreting the heritability of criminality. But see next point.
5) Barnes et al are right: I do twin studies for a living, and it would be mighty hypocritical of me to declare that they are useless in general. As a BG person who has spent a lot of time criticizing the heritability concept, I have made it a discipline to never suggest that my doubts about numerical heritabilities should lead to a general dismissal of genetic effects on behavior or the behavior genetic enterprise generally. The one thing that is for sure about the heritability of behavior is that it isn't zero (or one), and while I doubt that this fact has deep implications for how we think about ourselves as human beings (we already knew that we were biological, genetic beings), it has profound implications for how we conduct ourselves as social scientists. Bottom line, it means that we can never interpret correlations among biologically related people, or within individual people across time, as necessarily environmental in origin. This fact has nothing to do with numerical heritabilities, the EEA, rDZ=.5, the additivity of genes and environment, or any of the other long-standing bones of contention. It is true under the loosest possible interpretation of the meaning of quantitative genetics.
6) I suspect that Burt and Simons think they have this point covered. Early in their first paper, they have a very nice paragraph (bottom of 225) about how they have no intention of dismissing the importance of genes for criminal behavior, or of endorsing radical environmentalism or social determinism. That's a nice sentiment, but I don't think they live up to it. Where in the remainder of their articles is a concession that genetic pathways rule out certain interpretations of the data, an acknowledgement that criminology has to take genetics into account when it is interpreting its findings? Like every anti-BG paper I have ever read, they spend the rest of their paper finding something to attack in every single genetically oriented paper they can find. Twin study? EEA. Adoption study? Prenatal effects. If all of non-experimental social science were held to this standard it would just go away. The fuzziness of the "heritability study" concept allows them to fade from doubts about heritability coefficients, with reasonable citations to me, to dismissal of behavior genetics or even quantitative genetics in general, which is wishful thinking and for which I offer no support.
7) Basically, I think post-heritability twin studies are useful as quasi-experimental tools to investigate causal hypotheses about observed associations when random assignment is impossible. The best citation to my ideas about how twins can be used to do useful social science is Turkheimer and Harden (2014), in Reis and Judd, Handbook of Research Methods in Social and Personality Psychology. It's a commercial book and I won't post the link here, but if buying it presents a financial hardship let me know.
8) Now the question is whether the studies that Burt and Simons list are h2-equals-studies or more interesting genetically informed social science. I'm not going to take the time to go through them one at a time, but the several I looked at were bivariate "quasi-causal" (as we call them in our lab) studies. Ironically, the ones I looked at were actually quite consistent with phenotypically causal interpretation, ie the effects don't go away when you control for genetics. This is something that genetic researchers often miss: they think they are supposed to be interested in genetic pathways, A effects, but in fact the interesting hypotheses are usually about E effects, associations within identical twin pairs that remain with genetic differences controlled. See Turkheimer and Harden.
9) Moffitt and Beckley wrote a nice reply about epigenetics and I won't go into depth about it. I think that people who think that epigenetic explanations of behavioral differences are important should go ahead and do the research and show it. I doubt very much that a demonstration of meaningful epigenetic effects would meet with any opposition in the behavior genetic community. Epigenetics of behavior is behavior genetics. Epigenetics and classical genetics aren't at odds on a biological level, and there is no reason they should be at odds in social science.
10) Like a lot of recent anti-BG theorists, Burt and Simon are just wrong about GCTA. I have my doubts about some aspects of GCTA, discussed here. But Burt and Simons cherry pick the few studies that have produced zero GCTA-heritabilities, and ignore the many others that look almost exactly like twin studies with somewhat smaller effects. And it makes perfect sense inside the paradigm that the effects would be smaller. Differences between twin heritabilities and GCTA heritabilities are interesting, varied in magnitude, and as far as I know still awaiting thorough theoretical explanation. But the idea that GCTA has shown that twin studies were wrong all along isn't even close. In fact, the conclusion of my GCTA paper captures my overall thoughts on heritability in both directions, as follows, noting especially the first sentence:
The Visscher et al. (2010) program should drive a stake
through the heart of a classical line of argument
against classical behavioral genetics and
its attendant statistical assumptions.
Nevertheless, it is
difficult to see how their
will make much of an impact on the more contemporary problem, which is
that quantitative genetics, despite demonstrating the universality of heritability,
has failed to offer much in the way of
etiological insight into complex behaviors, and moreover that the very ubiquity of
heritability has made it problematic
to differentiate
between heritable phenotypes that have genetic mechanisms and those that
do not.
So in conclusion: if you want to cite me as a critic of some general version of BG, the citation should be limited to the idea that numerical heritabilities aren't very important per se, and that studies that do nothing other than estimate them are no longer very important. The next sentence should be something about how I do maintain that nonzero heritability is important methodologically, and that there are many scientifically useful things to do with twins other than just estimating heritabilities. Better yet, be very specific about what it is I am supposed to have said when you cite me.
One more self-quote and I'll shut up. At the end of my 1998 paper (Almost 20 years ago! Yikes.) I said,
I will close with two recommendations, one very practical and the other theoretical, for future discussions of nature-nurture. The practical suggestion is that all sides of the issue should stipulate the first law of behavioral genetics and refrain from further discussion of whether or not the heritability of anything is equal to zero. As a reader of behavioral genetics, keep a pencil by your side and lightly excise everything either asserts nonzero heritability or attempts to explain it away: Much space could be saved in our journals (even those containing sophisticated multivariate genetics or well-informed opposition) if this recommendation were put into effect.
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